| HOME | HELP | FEEDBACK | SUBSCRIPTIONS | ARCHIVE | SEARCH | TABLE OF CONTENTS |
|
|
|
|||||||
|
|||||||||
Letters and Responses |
It was with great interest that we read the article titled "Adding Ultrasound in the Management of Soft Tissue Disorders of the Shoulder: A Randomized Placebo-Controlled Trial" by Kurtais Gürsel et al in the April 2004 issue of Physical Therapy. The authors have attempted to determine whether the common clinical practice of adding ultrasound (US) in conjunction with other modalities (moist heat and interferential current) and exercise is superior when compared with a similar treatment with sham US in a patient population.
After 3 weeks (15 visits), improvements in both groups were noted when their measurements were compared with their baseline measurements (pain intensity, passive and active range of motion, and scores on 2 questionnaires [Health Assessment Questionnaire and Shoulder Disability Questionnaire]). No differences, however, were noted between groups. The authors concluded that "it is apparent that adding US to a well-planned intervention regimen has no benefit." Although the study has several strengths, we disagree with this conclusion. First, we believe the method utilized may have precluded the independent variable (true US) from reaching the source of pathology. Second, the conclusion is too broad given the scope of the study.
Regarding the method, we contend that, with the exception of the beam non-uniformity ratio, which we assume was erroneously reported as 1:6 and not 6:1, the authors selected a reasonable set of variables, including frequency, intensity, duration, and effective radiating area related to the ultrasound treatment.1,2 We do have concerns, however, regarding patient positioning and therefore the location to which treatment was administered. As 17 of the 20 subjects in the "true US" group had diagnoses of supraspinatus tendon involvement (either tendinosis or partial rupture), it is very unlikely the US reached this soft tissue given the patient positioning described in the article. Subjects in this study were positioned with their forearm supinated and their arm resting in their lap. In this position, the subjects' shoulder was likely placed in a small amount of flexion. In this posture, the supraspinatus tendon is positioned under the acromial process.3,4 To adequately manage this soft tissue disorder with US, we argue that the shoulder would be better positioned if placed in extension. We lack data, however, to confirm whether this placement would be better than that used by the authors. With the shoulder in extension, the supraspinatus and rotator cuff tendons are, in theory, moved anteriorly from under the acromial process and into a palpable position, thereby, we contend, exposing the tendon to the application of US. This, however, is a theoretical argument and not one that is currently supported by direct evidence for either the greater penetration of US or the benefits of intervention.
We agree with the authors that more evidence is necessary regarding the efficacy of US; however, based on the results of this study, we argue that the authors can conclude only that US was not beneficial to this group of subjects in the context of the designated US settings used and the patient positioning. Before concluding that US is not effective as an added intervention in the management of soft tissue disorders of the shoulder, we contend that additional studies are warranted. Specifically, we believe that alterations in treatment variables and patient positioning in this population as well as in patients with other painful shoulder conditions should be examined.
Department of Physical Therapy
Rangos School of Health Sciences
Duquesne University
Pittsburgh, PA 15282
carcia{at}duq.edu
Department of Physical Therapy
Rangos School of Health Sciences
Duquesne University
Doctoral Student in Rehabilitation Sciences
Duquesne University
References
I contend that there are problems with the method, subject selection, interventions, and outcome measures, all of which I view as combining to limit the validity of the authors' conclusions.
This study was not double-blinded. The treating therapist knew who received true US and who received sham US. Although this knowledge would likely bias the results in favor of, rather than against, an effect of the intervention, the impact is not predictable. In addition, there is no mention of a power analysis to determine the appropriate number of subjects to detect the expected size of effect.
The subjects in this study had a wide range of diagnoses; the only commonalities were more than 4 weeks of shoulder pain and restricted range of motion (ROM). It also is likely that the underlying pathology in these patients was at various stages of healing, which, based on current evidence from animal studies, are likely to benefit from different US doses. Previously published studies have demonstrated that pulsed low-dose US is most effective for facilitating tissue healing,1–4 whereas continuous high-dose US has been shown to be most effective for increasing tissue temperature, which will increase tissue extensibility and thus facilitate greater gains in ROM with stretching.5,6 In addition, in the absence of true controls who do not receive any intervention, the changes in these patients cannot be compared with the natural course of improvement of these conditions.
The intervention under investigation in this study was therapeutic US. This US was applied at an intensity of 1.5 W/cm2, with, I presume, a continuous duty cycle, although this is not stated, for 10 minutes to an area 3 times the effective radiating area (ERA) of the sound head used. This would be predicted to increase the temperature of the area by 2°C,6 which is not sufficient to reach the recommended goal of 40° to 45°C to produce thermal effects.5 In addition, the US was applied "over the superior and anterior periarticular regions of the glenohumeral joint," not an area likely to be the source of a restriction of ROM. If this area was the source of the patients' pain, then the pain most likely was due to inflammation and would be expected to respond to a low dose of pulsed US, and even potentially to be adversely affected by the heating produced by continuous US. This approach to applying an intervention, in this case US, to a patient without consideration of findings from a thorough examination is contradictory to the approach recommended for physical therapy interventions by the Guide to Physical Therapist Practice.7
Furthermore, the many other interventions applied to the subjects in this study, including hot packs, sensory-level interferential electrical stimulation, and various exercises, could be expected to obscure an effect of US over a 2-week period. This concern is supported by the results of this study, as shown in Table 2, demonstrating improvement in all measurements for all subjects.
The outcome measures used in this study also limit the conclusions that can be drawn. A 4-point pain scale, in my view, has limited sensitivity. The ROM measurements also were not shown to be reliable or valid. Although the report does state that the assessor practiced to improve the reliability of her measurements, no information on the reliability or validity of her measurements is provided.
Given the limitations of this study, I believe the only conclusion that can be drawn is that the addition of US with a frequency of 1 MHz and an intensity of 1.5 W/cm2, applied with a transducer head with an ERA of 5 cm2 to a 15-cm2 area over the superior and anterior periarticular regions of the glenohumeral joint, in patients with pain and decreased ROM of the shoulder does not provide a large additional benefit beyond those produced by exercise, hot packs, and sensory electrical stimulation combined. These findings are to be expected because the interventions are not consistent with current evidence-based recommendations and the study design was unlikely to be able to detect a treatment effect. This is very different from the authors' conclusion that "there is insufficient evidence to support the use of 1-MHz ultrasound in combination with other interventions in the management of painful shoulder conditions."
michcameron{at}yahoo.com
References
Not all exercise is the same kind of exercise; there is tremendous variability and complexity to stretching, strengthening, and all of the other exercise interventions we use in our profession. Conducting a general study on a nonspecific type of exercise is unheard of in this decade of specific and objective research. Likewise for our modalities such as ultrasound (US). Ultrasound is not a "generic" modality. The mechanical and thermal effects of this intervention are distinct, and I believe that the outcome depends on applying the modality correctly.
A study done by Ebenbichler et al1 is an excellent example of how a specific setting of US (pulsed) can demonstrate positive clinical results for management of a specific diagnosis (calcific shoulder tendinitis) in a randomized controlled trial. In other studies, parameters of US were used that were inappropriate for the purpose of the intervention. Falconer et al2 used continuous US at an intensity of 1.0 W/cm2 on arthritic knees. Based on Leung et al3 and Millett et al,4 this is an inappropriate setting if the knees are at all inflamed and, therefore, will yield nonsignificant or poor results. Similarly, Lundeberg et al5 used continuous US in the management of lateral epicondylitis when, based on Belanger,6 pulsed US would have been the appropriate modality. Hashish et al7 demonstrated negative effects of US in reducing inflammation. However, the intensity of 1.5 W/cm2 that they used, which will increase blood flow to the tissue, was inappropriate to reduce inflammation.6 Kurtais Gürsel et al managed all shoulder problems with thermal US, which is contraindicated for many of the types of patients in their study who had inflammatory problems.6
When reading the literature about US, the parameters of the intervention must be carefully scrutinized.
CLEWISPHD{at}aol.com
References
In our study, there were some limitations, such as the heterogenity of the patient groups regarding the duration of the symptoms and the diagnosis. The patients were probably in different stages of healing, but there were no acute cases, and the cases were mostly chronic. This explains why patients were treated with 1.5 W/cm2, which is within the intensity range proposed by Khan.6 The use of low intensities (less than 1.0 W/cm2) is recommended to achieve maximum healing rates in inflamed tissues,7 but there are no quantitative or scientific data indicating that higher intensities are harmful.8 Furthermore, Jackson et al9 showed that the mechanical properties of injured tendon could be improved with US, and the intensity used in their study was 1.5 W/cm2. The thermal properties of US have been shown to increase elasticity and decrease the viscosity of collagen fibers and soft tissue, thus allowing for greater residual length gains while reducing the risk of damage through the applied stretching force. The change in viscoelastic properties is transient, and, in order to achieve optimal effects, the stretching should be applied during or immediately following heating.10,11 Concerning these data, exercise was added to the treatment in this study.
We would like to address some of the specific criticisms of our study. Carcia is absolutely right about the beam nonuniformity ratio, which was erroneously reported as 1:6 and not 6:1. Regarding Carcia's comment that we did not define the patients' position during treatment precisely, the patients were sitting on a table with their hands supinated in their lap and placed far from each other so that the shoulder was in extension. We assume that is the position in which the components of the rotator cuff can be exposed to US. This position also allowed the bicipital tendon to be treated by US for the patients who had bicipital tendinitis.
Both the patients and the assessor were masked throughout the study. The treating physical therapist was not masked. It would have been difficult for us to mask the treating therapist because an experienced therapist can discern whether true or sham US is applied from the rate of disappearance of the transmission gel. In addition, the role of the treating therapist was to administer the planned treatment without intervening, and she had no role in assessing or informing the patient in any of the steps of our study design.
The outcome measures used in our study also were questioned regarding limited sensitivity. The Shoulder Disability Questionnaire, however, was shown to yield valid data and to be sensitive to change.12 The Likert-type pain scale was preferred in this study because, in our daily practice, we feel that Turkish patients respond better to this scale. Personal feeling, however, is not sufficient to decide which outcome measures to use, and the evidence comes from the studies in which Likert-type scales correlated well with visual analog scales.13–15
We believe that the comparison made in our study is valid: after randomization, the relatively small groups were comparable with respect to prognosis, and groups were comparable regarding extraneous factors, such as exercise treatment. Moreover, to date, evidence is lacking that, for a given shoulder complaint, one type of exercise is more effective than another.
In contrast to confidence intervals, an a priori sample size calculation does not contain valuable information regarding the precision or statistical power of the study. To date, regardless of the results of our study, evidence is lacking that, for a given shoulder complaint, one US dosage is more effective than another.
Thus, within the context of our study—although there are some pitfalls—we conclude there is still insufficient evidence to merit use of 1-MHz, continuous, 1.5 W/cm2 US in the treatment of patients with soft tissue disorders who are in the subacute-chronic phase when added to other physical agents such as hot packs or electrical stimulation.
Department Physical Medicine and Rehabilitation
School of Medicine
University of Ankara
06100 Ankara, Turkey
ykurtais{at}ttnet.net.tr
Specialist in Physical Medicine and Rehabilitation
Department of Physical Medicine and Rehabilitation
Bayindir Hospital
Ankara, Turkey
Department of Physical Medicine and Rehabilitation
School of Medicine
University of Ankara
Department of Physical Medicine and Rehabilitation
School of Medicine
University of Ankara
Clinical Epidemiologist and Physiotherapist
Julius Center for Health Sciences and Primary Care
University Medical Center
Utrecht, the Netherlands
References
Both Cameron and Lewis declare that the US parameters used were inappropriate for these patients. For example, Cameron states, "It also is likely that the underlying pathology in these patients was at various stages of healing, which, based on current evidence from animal studies, are likely to benefit from different US doses. Previously published studies have demonstrated that pulsed low-dose US is most effective for facilitating tissue healing...." In a similar vein, Lewis references studies, including the study by Kurtais Gürsel et al, that were negative for an added benefit of US and suggests that the parameters were wrong for the conditions being treated. In contrast, Carcia et al state that Kurtais Gürsel et al "selected a reasonable set of variables, including frequency, intensity, duration, and effective radiating area related to the ultrasound treatment."
It is obvious that, with respect to the US parameters used in the study by Kurtais Gürsel et al, we are confronted with "dueling opinions." Cameron and Lewis believe that continuous wave US is inappropriate for the conditions described in the article (because of the "inflammatory" nature of the condition), whereas Carcia et al consider continuous wave the proper treatment. However, and perhaps even more important, can we be certain that "inflammation" is a component of the pathology that was treated in these patients? Certainly not according to Khan et al,1 who contend that "since painful overuse tendon conditions have a non-inflammatory pathology," the term "tendinitis" is incorrect, based on histopathological studies. Indeed, Khan et al favor the terms "tendinosis" or "tendonopathy," rather than "tendinitis," because "within two to three weeks of tendon insult tendinosis is present and inflammatory cells are absent."1 Therefore, the arguments of Cameron and Lewis may be based on incorrect assumptions about the pathology being treated.
But this brings us to an interesting question. Why are there such strong but opposing opinions among the letter writers? Possibly in part because these clinicians have observed patients benefiting although each uses different US parameters. But if different US parameters are associated with good clinical outcomes in their hands, this leaves us with 2 possibilities: (1) benefits accrue regardless of the form of US chosen, or (2) neither form of US affords any added benefit, meaning the benefits observed by both groups of letter writers are due to the other treatments given in addition to the US (which brings us back to the results of the paper that started all this). There is obviously no unanimity of opinion among clinicians concerning many aspects of therapeutic US.
Some questions raised by the letter writers might have been answered by greater detail in the method section. Kurtais Gürsel et al describe how the modalities of US, moist heat, and electrotherapy were delivered and then comment on the passive and active exercises—but not the sequence with which these procedures were applied—and, perhaps most important for the US, how much time (if any) elapsed between giving the US and the institution of the exercises (eg, stretching, ROM). For example, did the stretching commence before the tissues cooled down? A method section that contains sufficient information for a reader to reproduce the work would include detailed descriptions of just how the treatments flowed in order to convince readers that the US was given its maximum opportunity to show a benefit, if a benefit is added. Kurtais Gürsel et al may indeed have applied the various components properly, but the review team, of which I was a member, did not ask them to supply the necessary information.
References
As detailed in the authors' response, the chronicity of the problems being treated also seems to provide a reasonable rationale for the authors' choice of continuous US. As discussed above by Dr Spielholz, the numerous and conflicting suggestions found in the letters regarding the mode, dosage, and treatment area for the US treatment underscores the contention of Kurtais Gürsel et al that there is no consensus regarding optimal treatment parameters.
Furthermore, despite the contention that use of incorrect US parameters would actually be harmful, no such results are apparent. Some of the letters suggested that the treatment approach should have been "optimized" for each patient, but the investigators' choice to use a standard treatment protocol for the US is a classic case of strengthening the internal validity of the study (by limiting extraneous variables) while somewhat weakening the external validity (by making it difficult to generalize to other modes of US treatment). On the other hand, the authors also were criticized for including multiple diagnoses and multiple treatments, both factors that enhance the external validity of the study. We would all like to see studies that are tightly controlled but still can be generalized to real-world situations; however, in most cases, there is a trade-off between internal and external validity,1 and researchers often are forced to make decisions favoring one or the other.
One issue that I believe has greater merit is the concern expressed by Carcia and colleagues that the shoulder position might not have allowed for adequate exposure of the supraspinatus tendon during the US treatment. The authors have clarified in their response that although the patients' hands were on their laps, the "[hands were] placed far from each other so that the shoulder was in extension." There is evidence, however, that maximal exposure of the supraspinatus tendon is obtained in a position of shoulder adduction, medial rotation (80–90 degrees), and hyper-extension of 30 to 40 degrees.2 Thus, the arm position during the US treatment may have been less than optimal for the supraspinatus tendon, though it would still seem appropriate for treatment of the biceps tendon. A more exact description of the arm position would have been helpful and may have led to the issue of shoulder positioning being addressed during the review process rather than retrospectively.
Another criticism raised in the letters is that the conclusion of the paper was overstated. The conclusion section begins with the following statement: "Based on the literature and the results of our study, we conclude that there is insufficient evidence to merit wide use of 1-MHz US in combination with other interventions in the management of painful shoulder conditions." In their response, the authors have modified their conclusion statement slightly to clarify the mode and dosage of the US treatment, whereas some of the letters suggested even more caveats were necessary to avoid overstating the conclusion. Although the conclusion section may not have included all of the possible caveats, careful reading of the paper as a whole reveals that the authors did acknowledge many of the limitations. For example, the discussion section mentions the limitations related to multiple treatments, the lack of a true control group, and the lack of statistical power, whereas the methods section, in my opinion, clearly delineates the mode and dosage of the US treatments used in this study.
Open debate in the form of Commentaries or Letters to the Editor and the subsequent responses by authors is healthy and informative, and the authors of the letters published here should be commended for raising some pertinent issues. I believe that publication of the paper by Kurtais Gürsel et al and publication of these letters and responses may result in two positive outcomes. First, I believe that the study results strongly support the efficacy of short-term, conservative treatment of shoulder soft tissue disorders, even when the symptoms have been present for many months or even years. Second, the debate regarding the investigative approach taken by Kurtais Gürsel et al may motivate more clinicians, including those involved in this debate, to produce more and better clinical trials addressing the issues raised here.
References
CiteULike 
Complore 
Connotea 
Del.icio.us 
Digg 
Reddit 
Technorati What's this?
Related Article
| ||||||||||||||||||||||||||||||||||||||||||||||||||||||||||||||||||||||||||||||||||||
| HOME | HELP | FEEDBACK | SUBSCRIPTIONS | ARCHIVE | SEARCH | TABLE OF CONTENTS |
